Dear Authors,

Thanks for improving the manuscript to answer the two reviews. I still fill however that the main points of reviewer #1 have not been adequately answered; in particular you present your modifications as an overall improvement of dust simulations in WRF-CHEM, but the manuscript focuses only a short period of time, and on a single dusty region, without comparing to observations. In my opinion, you are not proving that your modifications do represent an improvement : you should compare to global observations (surface concentration and AOD), over a longer period of time in order to be able to assert this.

Besides, some answers to reviewer comments, and in particular about the sea-salt and dust coefficients for PM2.5 and PM10 calculations, are incomplete: you mention that "Coefficients d_25, s_25, d_10 in eq.2 are obtained assuming that the aerosol size distribution is a function of ln(r). This method is acknowledged in CAMS reanalysis
( https://confluence.ecmwf.int/pages/viewpage.action?pageId=153393481 )". I had a look to the webpage and they don't mention anything about the aerosol size distribution for PM compuration.

Still, I realize that your manuscript represent a large amount of work, and some modifications are of interest. I think you should try to use a broader range of simulations and comparison to observations to prove your point and hope your will resubmit a new manuscript that goes in this direction.

Kind regards,
Samuel Remy

Dear authors,

The reviewers agreed that the revised manuscript is an improvement over the first version. However, some concerns still remain. Could you please upload a new version that answers to the specific comments below:

1) I am still not convinced that using natural logarithm of particle radii (ln(r)) is better than using particle radii (r) unless the authors can show me that there is indeed a smoother function of ln(r) than r for aerosol size distributions. The authors can probably check this by making line plots of aerosol size distributions as a function of ln(r) and r. I don’t buy the authors’ argument simply because CAMS uses this way.
2) The inclusion of the 7-month (June 1 to December 31, 2016) case study clears out a lot of my concerns. One thing I would like to see is the PM2.5 version of Figure 8. Clearly, PM10 concentrations are overestimated by the uncorrected model run. I would like to know to what extent the observed PM2.5 concentrations are resolved by both runs if there are PM2.5 observations. Also, using C=0.8 for the ALL_OLD run and C=0.5 for the ALL_OK run does not seem to provide a fair comparison. Either the authors need to run the ALL_OLD with C=0.5 or the authors need to provide convincing justification.
3) There are many sections in the Appendix and I am wondering if all of the sections are necessary. I got a little bit lost when I read through the sections.

Even minor suggestions:

1) Page 1, line 15: Middle East (ME) should be defined here instead of in Abstract since supposedly Abstract and the main text should be self-explanatory.
2) Table 1 caption: Since there are more options than what are listed here, the authors need to add that these are the likely options that may be affected by the corrections.
3) Figure 1 caption: “The red square corresponds to dust emission area for doing dust mass balance experiment.”
4) Page 14, Line 8: Should be either “For a larger domain” or “For larger domains”.
5) Page 14, Line 14: NOT_FIXED_GRAV_SETTLING should be introduced before.
6) Page 17, Lines 4-5: The statement “Figure 9 demonstrates the ….” Is not clear to me, please re-phrase.

* The authors have not addressed whether the assumption of a size distribution that is a function of ln(r) matches the internal assumptions of GOCART or not. (The PM formulae in CAMS do assume this, as pointed out, because the assumed size distribution within the aerosol scheme used in CAMS itself is log-normal.) That doesn't mean it would be appropriate for some other model that internally assumes e.g. a uniform distribution across each size bin.) The same applies also to the assumed size distribution in MOSAIC when considering the bin mapping between that and GOCART.

* Despite comments from multiple reviewers, several parts of the manuscript still talk about differences from ALL_OK as though that was truth and therefore differences from it are "overestimation" or "underestimation". Such language is not justified without reference to actual observations of PM concentrations or column dust mass as the case may be.

* There are still an excessive number of references in parts of the introduction without any real discussion of what they show.

* It is mentioned in passing (p.15) that C is tuned differently between ALL_OLD and ALL_OK. This calls into question which results are due to the changes in the scheme itself, and which due to the retuning of this factor. It's essential to discuss and disentangle these two aspects, probably with the aid of a third simulation.

Kind regards,
Samuel Remy

Dear authors,

Nearly there! Thank you for answering the second round comments from the reviewers. I think your manuscript is nearly ready for publication; I just have one comment/question: how much of the decreae and improvement in PM10 can be attributed to the modified C factor between ALL_OK and ALL_OLD? If (as probable) it is an important factor, this should be mentioned.

Kind regards,
Samuel